Principles of study design in environmental epidemiology

Principles of Study Design in Environmental Epidemiology Hal Morgenstern 1* and Duncan Thomas2 Department of Epidemiology, University of California at Los Angeles, School of Public Health, Los Angeles, CA 900241772; 2Department of Preventive Medicine, University of Southern California, School of Medicine, Los Angeles, CA 90033-9987

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Abstract This paper discusses the principles of study design and related methodologic issues in environmental epidemiology. Emphasis is given to studies aimed at evaluating causal hypotheses regarding exposures to suspected health hazards. Following background sections on the quantitative objectives and methods of populationbased research, we present the major types of observational designs used in environmental epidemiology: first, the three basic designs involving the individual as the unit of analysis (i.e., cohort, crosssectional, and case-control studies) and a brief discussion of genetic studies for assessing gene-environment interactions; second, various ecologic designs involving the group or region as the unit of analysis. Ecologic designs are given special emphasis in this paper because of our lack of resources or inability to accurately measure environmental exposures in large numbers of individuals. The paper concludes with a section highlighting current design issues in environmental epidemiology and several recommendations for future work. -Environ Health Perspect 101(Suppl 4):23-38 (1993). This manuscript was prepared as part of the Environmental Epidemiology Planning Project of the Health Effects Institute, September 1990 - September 1992. This work was funded by the Health Effects Institute in Cambridge, MA. The authors would like to thank Dr. John Tukey, Dr. Sander Greenland, and other members of the HEI Methodology Working Group for their helpful comments.

Introduction The purpose of this article is to discuss the principles of study design and related methodologic issues in environmental epidemiology. The focus is on studies aimed at evaluating causal hypotheses regarding exposures to suspected health hazards. Because the intended audience for this document includes scientists without formal training in epidemiology, parts of this article highlight basic principles of epidemiologic research. Nevertheless, we also try to summarize comprehensively the current state of the art and make recommendations for future developments in study design. For more extensive treatment of general research principles and methods in epidemiology, the interested reader should consult available textbooks in this area (1-6). More detailed examples of applications in environmental epidemiology may be found in several other books, such as those edited by Leaverton (7), Chiazze et al. (8), Goldsmith (9), and Kopfler and Craun (10). Population Parameters The major quantitative objectives of most epidemiologic studies are to estimate two types of population parameters: the frequency of disease occurrence in particular populations and the effect of a given exposure on disease occurrence in a particular population. Measures of disease frequency involve the occurrence of new cases or deaths (incidence/mortality) or the presence of existing cases (prevalence). In both applications, the number of cases is expressed relative to the size of the population from which the cases are identified. With incidence measures, this denominator is the (base) population at risk (i.e., individuals who are eligible to become cases). Thus, the base population of a study (or study base) is the group of all individuals who, if they developed the disease, would become cases in the study (3,11,12). Disease incidence, which is central to the process of causal inference, can be expressed as a cumulative measure (risk) or as a person-time measure (rate). The cumulative incidence (incidence proportion) or average risk in a base population is the probability of someone in that population developing the disease during a specified

period, conditional on not dying first from another disease (13). The term cumulative incidence or cumulative incidence rate also is defined somewhat differently as the integral over the follow-up period of the hazard (rate) function (14). The incidence rate or instantaneous risk (hazard) is the limit of the average risk for a given period, per unit of time, as the duration of the period approaches zero. The average rate (incidence density) for a given period is estimated as the number of incident events divided by the amount of person-time experienced by the base population. For example, a rate of 0.001/year means that we would expect one new case to occur for every 1000 person-years of follow-up (e.g., 100 disease-free people followed for an average of 10 years). Although there are many quantitative methods for expressing the magnitude of a statistical association between two variables (e.g., exposure status and disease occurrence), we are usually interested in a special class of such measures that reflect the net effect of the exposure on disease occurrence (i.e., causal parameters). In general, a causal parameter for a target population is a hypothetical contrast-in the form of a difference or ratio--between what the frequency of disease would be if everyone were exposed (at a given level) to what the frequency would be if everyone were unexposed (often called the reference level) (15). When this difference for a specific exposure is not zero (the ratio is not one), we say that the exposure is a risk factor for that disease in the target population. In practice, we estimate causal parameters indirectly by comparing disease frequency for an exposed group with disease frequency for an unexposed group. Epidemiologists typically estimate the risk or rate ratio (often called the relative risk) by comparing the exposed population with an unexposed population. The key assumption of this statistical approach is that the risk or rate observed for the unexposed group is the same (within confounder strata) as the risk or rate that would have been observed in the exposed group if that group had not been exposed (16). Thus, the (true) risk ratio may be interpreted as a causal parameter, which is the number of cases actually occurring in the exposed (target) population divided by the number of cases that would have occurred in the absence of exposure. Certain measures of association, such as correlation coefficients and standardized regression coefficients, do not, in general, reflect any

causal parameters. The reason is that the magnitude of these measures depends in part on the relative variances of the exposure and disease variables, which are influenced by the sampling strategy (i.e., noncausal parameters) (17,18). Another measure of association, the odds ratio, is used in certain types of epidemiologic studies (casecontrol designs) to estimate the risk or rate ratio indirectly when we cannot first estimate the incidence rate or risk in the exposed and unexposed populations (1-6,19,20). Problems in Environmental Epidemiology There are several general problems in environmental epidemiology that tend to limit causal inference and, therefore, shape design decisions. Long Latent Periods. The interval between first exposure to an environmental risk factor (or the start of causal action of this factor) and disease detection (or symptom onset) may be many years or even decades. Such long latent periods are partly due to limitations of medical technology and incomplete surveillance for detecting disease; yet they are also due to a prolonged induction period in which years are needed for the disease process to begin (5). The term latent period also is used more specifically to indicate the hypothetical interval between disease initiation and detection (5). Refer also to Armenian and Lilienfeld (21) who discuss alternative definitions of latency. Unfortunately, long latent periods produce important practical constraints on our ability to estimate exposure effects. The investigator must either observe subjects for many years or rely on retrospective (historical) measurement of key variables. The latter alternative may be infeasible for certain types of exposures or in certain populations. Even when feasible, however, retrospective measurement usually increases the amount of error with which exposures are measured (see below). Furthermore, the level of most environmental exposures and many extraneous risk factors changes appreciably or unpredictably over time; long latent periods, therefore, seriously complicate our ability to estimate effects (22). Errors of Exposure Measurement. A major challenge in environmental epidemiology is to measure accurately each individual's exposure to hypothesized risk factors (i.e., the biologically

relevant dose [Thomas and Hatch, this issue]). This task is made very difficult by the lack of information about environmental sources of emission, the complex pattern of most long-term exposures, the individual's ignorance of previous opportunities for exposure, the lack of good biological indicators of exposure level, and the lack of sufficient resources to collect individual exposure data on large populations. The consequences of exposure mismeasurement are probable bias in the estimation of effect (see "Sources of Epidemiologic Bias") and possible loss of precision and power with which effects are estimated and tested (23,24). The problem and issues of exposure measurement are discussed more thoroughly by Hatch and Thomas in this issue. Rare Diseases, Low-Level Exposures, and Small Effects. In most epidemiologic studies of environmental hazards, statistical objectives may be further compromised by the infrequent occurrence of the disease or outcome of interest, by the low prevalence or levels of environmental exposures in the general population, and by the search for small effects (for which the true rate ratio is between 0.5 and 2). A critical consequence of these features is usually substantial loss of precision and power with which effects are estimated and tested. In addition, it becomes more difficult for the investigator to separate the effect of the exposure of interest from the distorting effects of extraneous factors. Causal inference can then be seriously compromised. Research Objectives and Strategies Given the above problems, epidemiologists must carefully plan their studies, analyze their data, and interpret their findings. Inaccurate results reflect both random errors of estimation (chance) and systematic errors or bias. An epidemiologically unbiased or valid estimate of a causal parameter is one that is expected to represent perfectly (aside from chance) the true value of the parameter in the base population. Sources of Epidemiologic Bias A common framework for describing the validity of epidemiologic research is to consider three sources of bias in the estimation of

effect: selection bias, information bias, and confounding (2). Despite the practical attractiveness of this framework, the three types of bias are not entirely separate concepts. The amount of confounding, for example, can depend on how subjects are selected. Selection Bias. Selection bias means that the way in which subjects are selected into the study population or into the analysis (due to lost subjects or missing data) distorts the effect estimate. In general, this problem occurs when either disease status or exposure status influences the selection of subjects to a different extent in the groups being compared. Selection bias is most likely to be problematic when the investigator does not identify the base population from which study cases arose. Information Bias. Information bias means that the nature or quality of measurement or data collection distorts the effect estimate. The primary source of information bias is error in measuring one or more variables. When exposure status or disease status is misclassified, bias usually occurs. If the probabilities of misclassification of each variable are the same for each category of the other variable (nondifferential misclassification) and if the errors for different variables are independent, the estimate of effect is usually biased toward the null value (indicating no effect). Possible exceptions to this principle of nondifferential misclassification leading to conservative effect estimates arise when the misclassified exposure variable is categorized into more than two groups (25). In other situations involving differential misclassification (unequal misclassification probabilities) or correlated measurement errors, the effect estimate may be biased in either direction. In many studies, therefore, the magnitude of misclassification bias is difficult to predict, especially when other biases are operating. Confounding. Confounding refers to a lack of comparability between exposure groups (e.g., exposed versus unexposed) such that disease risk would be different even if the exposure were absent or the same in both populations (16). Thus, confounding is epidemiologic bias in the estimation of a causal parameter (see "Population Parameters"). Because there is no empirical method for directly observing the presence or magnitude of confounding, in practice we attempt to identify and control for manifestations of confounding. This is done by

searching for differences between exposure groups in the distribution of extraneous risk factors for the disease, which are called confounders. Thus, a confounder is a risk factor (or proxy) that is associated with exposure status in the base population. A covariate meeting these criteria is not a confounder, however, if its association with the exposure is due entirely to the effect of the exposure on the covariate; for example, the covariate might be an intermediate variable in the causal pathway between the exposure and disease. If the exposure and covariate are time-dependent variables, it is possible for that covariate to be both a confounder and an intermediate variable (see "Cohort Study"). The Need for Covariate Data In addition to the exposure of interest, there is the need in virtually all epidemiologic studies to collect data on other known or possible risk factors for the disease. These covariates may be relevant to the exposure effect in three ways: a) as confounders, b) as intermediate variables, and c) as effect modifiers. The effects of confounders must be controlled or removed analytically to obtain unbiased estimates of causal parameters. This control is usually achieved through stratification or model fitting. The assessment and control of intermediate variables can elucidate causal mechanisms that explain exposure effects (26). This approach often leads to new etiologic hypotheses and new intervention strategies for disease prevention. When the exposure-effect measure varies across categories or levels of another factor, we call the second factor an effect modifier; this statistical phenomenon is called effect modification or an interaction effect. The assessment of effect modification is model-dependent, meaning that it depends on what (causal) parameter is used to measure the effect (2-6). For example, an extraneous risk factor that does not modify the risk ratio for the exposure will modify the risk difference. The assessment of effect modification is important for properly specifying the predictors in statistical models (2,14), for making inferences about possible biological (causal) interactions between exposures (e.g., synergy) (5), and for generalizing one's results to other populations (see "Cohort Study").

Types of Research There are three general design strategies for conducting population research: a) experiments in which the investigators randomly assign (randomize) subjects to two or more treatment (exposure) groups; b) quasi-experiments in which the investigators make the assignments to treatment groups nonrandomly; and c) observational studies in which the investigators simply observe exposure (treatment) status in subjects without assignment (2). Although some epidemiologists classify the first two types as intervention studies, observational studies might also involve the evaluation of an intervention that was not implemented or controlled by the investigators. Social scientists often use the term quasi-experiment to mean any type of nonrandomized study (27). Experiments. In a simple experiment, there are usually two treatment groups. One group is assigned to receive the new experimental intervention and the other (control) group is assigned to receive no intervention, a sham intervention (placebo), or another available intervention. Simple randomization of individuals to treatment groups implies that all possible allocation schemes of assigned subjects are equally likely (28). Following randomization, the investigator follows subjects for subsequent disease occurrence or change in outcome status. A comparison of risks between treatment groups provides an estimate of a causal parameter reflecting the treatment effect. Because experiments are best suited ethically and practically to the study of health benefits, not hazards, experiments in environmental epidemiology would usually be limited to the study of preventive interventions. Furthermore, it is generally impossible or infeasible to randomize subjects individually. The only practical alternative, therefore, is to randomize by group, where the group might be a city, school, work site, etc. (29). The major limitation of group randomization is some within-group dependence (correlation) of the outcome variable, which reduces precision and power (30,31). Thus, the effective sample size falls between the number of randomized groups and the total number of subjects (see Prentice and Thomas, this issue).

As an example, consider the hypothesis that the intake of fluoride ions in drinking water has a protective effect on the occurrence of dental caries in children. An experiment might be conducted by randomly assigning many water districts (each with one fluoridedeficient water supply without treatment) either to implement sodium fluoride treatment under the control of the investigators or to continue its current policy of no treatment for the duration of follow-up. Assuming the hypothesis were true, we would expect the subsequent incidence rate of dental caries to be lower in the treated districts than in the untreated districts. Randomization insures a valid comparison of subjects according to intended treatment, i.e., assigned treatment, but not according to treatment actually received (16,28). That is, randomization of a sufficient number of units (subjects or groups) provides some assurance that the assigned treatment groups are comparable with respect to inherent risk. This does not imply that there can be no confounding in a comparison of randomly assigned groups. Even with perfect adherence to treatment assignments and no loss to follow-up, assigned groups might have, by chance, different hypothetical risks in the absence of treatment. Nevertheless, such confounding, if it exists, is equally likely to be positive or negative; conventional confidenceinterval estimates and p values reflect the possibility of this bias, which becomes smaller as the (effective) sample size increases (28). This protection against confounding afforded by randomization, however, does not apply to lack of adherence or loss to follow-up, both of which usually do not occur randomly. Furthermore, if some subjects cross over between treatments (e.g., residents of a fluoridated district obtain their water from nonfluoridated districts), a comparison of assigned groups will underestimate the true treatment effect even when the crossover is random (32). A comparison of compliers with noncompliers, on the other hand, is essentially observational and therefore prone to bias. Quasi-Experiments. A quasi-experiment may be done similarly to an experiment by comparing two or more nonrandomized groups, or it may be done by comparing one or more groups over time, before versus after the intervention is initiated in at least one group. With the latter approach, the composition of each group may change over time

so that subjects observed before the intervention are not the same subjects observed after the intervention. Returning to the fluoride hypothesis, a quasi-experiment was done in the 1940s and 1950s by comparing two similar, nearby cities in New York State, both of which lacked fluoride treatment before 1945. Newburgh started sodium fluoride treatment in 1945 and continued throughout the 10-yr postintervention follow-up period; Kingston continued to use its fluoride-deficient water without treatment (33). The investigators found that the rate of decayed, missing, or filled (DMF) teeth in children, ages 6 to 12, decreased by almost 50% in Newburgh but increased slightly in Kingston. Because subjects were not individually randomized in this study, it is possible that children in the treated group differed from children in the comparison group with respect to other risk factors for tooth decay, such as diet. Thus, the investigators' comparisons might have been confounded. Note, however, that randomization by city would not have reduced this possible bias in the Newburgh-Kingston study, because the two assigned treatment groups would be equally noncomparable regardless of which city was assigned fluoride treatment. Observational Studies. Unlike experiments and quasi-experiments, observational studies are commonly used to estimate the effects of exposures hypothesized to be harmful, fixed attributes (e.g., race and genotype), characteristics, behaviors or exposures over which the investigator has little or no control (e.g., weight, depression, and sunlight exposure), and other exposures for which manipulation or randomization would be unethical or infeasible. Observational studies are often conducted with secondary or retrospective data (instead of primary prospective data) and/or without following individual subjects for change in disease status. For example, the fluoride hypothesis could be tested by comparing the prevalence of decayed, missing, or filled teeth in children who live in areas supplied by fluoridated water with the corresponding prevalence in children who live in areas supplied by nonfluoridated water. Although such a study would be less expensive and easier to conduct than would the previous examples, there are additional methodologic problems that could lead to bias or misinterpretations.

The remainder of this article is devoted to an elaboration of observational study designs. In "Basic Observational Designs," we cover the basic designs in which data on disease status, exposure status, and all covariates are collected at the individual level; that is, the unit of analysis is the individual (or body part, such as the tooth or eye). In "Ecological Designs," we cover designs in which the unit of analysis is a group of individuals, such that information is missing on the joint distributions of key variables at the individual level. Basic Observational Designs Frequently, hypotheses about environmental risk factors for disease are derived from animal studies, clinical observations, reports of disease clusters, descriptive findings from population surveillance systems, and various types of exploratory studies (e.g., case series, mapping studies, and migrant studies). Formal testing of these hypotheses most often proceeds by conducting observational studies of the types described in this section. Basic designs in epidemiology may be classified according to two dimensions: type of study population and type of sampling scheme (34). First, the study population is longitudinal, involving the detection of incident events during a follow-up period; or it is cross-sectional, involving the detection of prevalent cases at one time. Second, the sampling strategy involves complete selection of the entire population from which study cases are identified, or it involves incomplete or case-control sampling of a fraction (